Pages

Wednesday, January 16, 2019

Particle physicists want money for bigger collider

The Large Hadron Collider (LHC) at CERN is the world’s current largest particle collider. But in a decade its days will come to an end. Particle physicists are now making plans for the future. Yesterday, CERN issued a press-release about a design study for their plans, which is a machine called the Future Circular Collider (FCC).

There are various design options for the FCC. Costs start at €9 billion for the least expensive version, going up to €21 for the big vision. The idea is to dig a longer ring-tunnel, in which first electrons would be brought to collision with positrons at energies from 91 to 365 GeV. The operation energies are chosen to enable more detailed studies of specific particles than the LHC allows. This machine would later be upgraded for proton-proton collisions at higher energies, reaching up to 100 TeV (or 100k GeV). In comparison, the LHC’s maximum design energy is 14 TeV.

€9 billion is a lot of money and given what we presently know, I don’t think it’s worth it. It is possible that if we reach higher energies, we will find new particles, but we do not currently have any good reason to think this will happen. Of course if the LHC finds something after all, the situation will entirely change and everyone will rush to build the next collider. But without that, the only thing we know that a larger collider will reliably do is measure in greater detail the properties of the already-known particles.

The design-reports acknowledge this, but obfuscates the point. The opening statement, for example, says:

“[Several] experimental facts do require the extension of the Standard Model and explanations are needed for observations such as the abundance of matter over antimatter, the striking evidence for dark matter and the non-zero neutrino masses. Theoretical issues such as the hierarchy problem, and, more in general, the dynamical origin of the Higgs mechanism, do point to the existence of physics beyond the Standard Model.” (original emphasis)

The accompanying video similarly speaks vaguely of “big questions”, something to do with 95% of the universe (referring to dark matter and dark energy) and raises the impression that a larger collider would tell us something interesting about that:

It is correct that the standard model requires extension, but there is no reason that the new physical effects, like particles making up dark matter, must be accessible at the next larger collider. Indeed, the currently most reliable predictions put any new physics at energies 14 orders of magnitude higher, well out of the reach of any collider we’ll be able to build in the coming centuries. This is noted later in the report, where you can read: “Today high energy physics lacks unambiguous and guaranteed discovery targets.”

The report uses some highly specific examples of hypothetical particles that can be ruled out, such as certain WIMP candidates or supersymmetric particles. Again, that’s correct. But there is no good argument for why those particular particles should be the right ones. Physicists have no end of conjectured new particles. You’d end up ruling out a few among millions of models, and make little progress, just like with the LHC and the earlier colliders.

We are further offered the usual arguments, that investing in a science project this size would benefit the technological industry and education and scientific networks. This is all true, but not specific to particle colliders. Any large-scale experiment would have such benefits. I do not find such arguments remotely convincing.

Another reason I am not excited about the current plans for a larger collider is that we might get more bang for the buck if we waited for better technologies. There’s the plasma wakefield acceleration, eg, that is in a test-period now and that may become a more efficient route to progress. Also, maybe high temperature superconductors will reach a level where they become usable for the magnets. Both of these technologies may become available in a decade or two, but they are not presently sufficiently developed so that they can be used for the next collider.

Therefore, investment-wise, it would make more sense to put particle physics on a pause and reconsider it in, say, 20 years to see whether the situation has changed, either because new technologies have become available or because more concrete predictions for new physics have been made.

At current, other large-scale experiments would more reliably offer new insights into the foundations of physics. Anything that peers back into the early universe, such as big radio telescopes, for example, or anything that probes the properties of dark matter. There are also medium and small-scale experiments that tend to fall off the table if big collaborations eat up the bulk of money and attention. And that’s leaving aside that maybe we might be better off investing in other areas of science entirely.

Of course a blog post cannot replace a detailed cost-benefit assessment, so I cannot tell you what’s the best thing to invest in. I can, however, tell you that a bigger particle collider is one of the most expensive experiments you can think of, and we do not currently have a reason to think it would discover anything new. Ie, large cost, little benefit. That much is pretty clear.

I think the Chinese are not dumb enough to build the next bigger collider. If they do, they might end up being the first nation ever to run and operate such a costly machine without finding anything new. It’s not how they hope to enter history books. So, I consider it unlikely they will go for it.

249 comments:

Do you know the essay “Six Cautionary Tales for Scientists” by Freeman Dyson? Although it was written in 1989 it seems extremely relevant again. (Since the essay is not freely available, I summarized some of the main points here http://jakobschwichtenberg.com/decentralization-science/)

This is correct. As I stress in my book, the prediction that the LHC had to find the Higgs or something like it was based on mathematically sound reasoning. Without the Higgs, the Standard Model has a problem.

However, the predictions for anything besides that were not based on mathematically sound arguments. They were based mainly on arguments from beauty. I explain this in great detail in my book. Even if you do not buy the arguments that I offered for why these predictions were no good, they did as a matter of fact not come true.

The important thing is now that this means there is *no* good argument for why a next larger collider should see anything besides the already known particles. There is no prediction of similar rigor as that for the Higgs (or other predictions for colliders before that).

"Therefore, investment-wise, it would make more sense to put particle physics on a pause and reconsider it in, say, 20 years to see whether the situation has changed, either because new technologies have become available or because more concrete predictions for new physics have been made."

Without going into the rest of your blog post, I think most of the particle physics community would disagree with this statement. If particle physics is put "on pause" for 20 years, the skillset currently present in the community in building and running these massively complex experiments will disappear in the absence of a clear target, as people with the necessary knowledge will slowly leave and students will be choosing careers in different fields. Starting to build an FCC from scratch would likely to be therefore a lot more expensive, despite technological advances that may or may not materialize in the meantime.

"...most of the particle physics community would disagree with this statement..."

No shit.

Look, we are currently paying for a lot of particle physicists. If we got rid of 90% of those we'd still have more than enough to pass on knowledge to the next generation. Besides, scientists write papers to make sure knowledge doesn't get lost. If particle physicists worry this may not work, maybe they should make more effort to write comprehensible papers.

Will they try to argue that they should continue to receive money? No doubt about this. Is this a convincing case to fund their research? No, it's not.

In the grand scheme of things, the amount of money is peanuts. Probably more is spent on tattoos and piercings.

Historically, many new instruments have found completely unexpected things, things which, by definition, there was no reason to expect. Some or most of these instruments had made a case to get funded, but, in hindsight, whether or not that played out doesn't really matter. So, I don't see the lack of expectation as a reason not to build it.

"In the grand scheme of things, the amount of money is peanuts. Probably more is spent on tattoos and piercings."

You are right, that amount over 10 or more years that the lab would take to build the FCC is literally peanuts. Sabine should perfectly know, for instance, that her country, Germany, spends 11.5 billion Euros per year to subsidize ineffective and basically issues useless photovoltaics... and will do that for 20 years!... This argument of hers, the "large" amount of money is just a specious one... it's fake news pure and simple.

I suppose it might come down to Forrest Gump, you never know what is in a box of chocolates until you open it. If nature has some structure that resonates at some energy ~ 1-10TeV or so we might then find it. You can't know until you look. The center for this has shifted from the US to the EU, and if this is not done it will probably shift to China --- along with everything else that is shifting to there.

I am not arguing whether or not it is worthwhile to build the FCC, although obviously I disagree with you on that front as well. I just wanted to highlight that it is extremely unlikely to be economically favorable to postpone the construction of a future collider, it would be like Intel deciding not to build a 7nm processors because it might be able to do a 5nm one later on. I don't know where you take the number of 90% from, do you think the LHC could run on 10% of its current personnel? The problem would obviously not be with theorists writing BSM papers on FCC physics, but engineers, accelerator physicists, and experimentalists, which make up a much larger fraction of CERN.

@Phillip and akidbelleWhile I agree that it‘s little money compared to what goes to waste in fruitless endeavours (say, trade wars, real wars, or simply stuff no one really needs but is made to think they need), that argument only makes sense if you imply that people / nations / whomever are actually willing to reassign money from „useless“ to - in this case - perceivedly somewhat less useless applications. Obviously, that’s not the case. There is only a limited budget for physics research, and out of that budget, as Sabine rightly points out, „better“ projects could be funded.

I hope you are not intentionally misunderstanding me. The 10%, needless to say, was a number I invented on the fly, not a serious estimate, and it was referring to times in which no particle collider operates.

Intel produces technologies for profit. Different game entirely. Do I really need to tell you that?

"Intel produces technologies for profit. Different game entirely. Do I really need to tell you that?"

You forget to say that Intel, like all other high-tech companies, profit from decades of publicly-funded R&D, on subjects that at the time they had been studied were as "useless" and "expensive" as the his vision research is.You simply lack the good perspective of things.

TWO new "not quite big enough" colliders? Is physics insane? Dump all that PRC and EU cash into one 300+ km circumference Big International Ring Collider in the desert wastes of southwestern Australia, powered by a few gigawatt nuclear reactors selling excess energy to Aussies.

When things are slow, dump BIRC beams tangent to the geoid to communicate with extraterrestrial planets. Nudge nudge, wink wink,

respectfully, if you say "Of course a blog post cannot replace a detailed cost-benefit assessment,", then your preceding statement "At current, other large-scale experiments would more reliably offer new insights into the foundations of physics." sounds like wishful thinking. And, it sounds like bashing others' work, a far easier task than convincing in better alternatives. For most of the population, the choice is not between an "excellent scientific project" and "an even better scientific project". Often it is between "funding science" and "building a wall".

Re: Any suggestion that 21 billion euros is "not that much money", or is in any way related to other expenditures, trade imbalances, or the like.

It is OTHER people's money, that we seem to be willing to spend with no good direction, and I think that is worth keeping in mind. The average taxpayer is the one that foots the bill. Do a survey asking the average taxpayer whether THEY agree that "21 billion euros is not that big of a deal", and see if the people who are the ones who will be footing the bill really think that way. Not a small gaggle of self interested theorists, and people who's industry will benefit from the project financially. The small gaggle has a biased opinion.

And comparing it to other expenditures or use of money, is a non sequitur, so we all recognize that?

Unless we think that all people's money is our own money to do with as we choose??

Good on you for being skeptical Sabine. Respect. Kudos. I knew there was a reason I liked you. (kidding, there are plenty of reasons).

And yes. To figure out the realistic project cost, we could probably examine initial estimate and actual expenditure on the LHC to get an idea of how much the project will overrun estimates.

"Do a survey asking the average taxpayer whether THEY agree that "21 billion euros is not that big of a deal", and see if the people who are the ones who will be footing the bill really think that way. "

Wrong question. Taxpayers like you should be asked the question "are 2,5€/year/person too much money"?

Because that's what it is 15 billion€ in 10 years for 600 million citizens of the CERN funding countries.

"i know this is going to cost more, but why not make it 200TEV or even 1000 TEV?"

Because already 50+50 TeV is at the limit of what could reasonably be built in 20 years. 200 TeV in the same tunnel would need 32 Tesla magnets, present ones are 8.4... 16 T for the FCC are deemed feasible in 10 years or so. A bigger tunnel is out of the question, this one of 98 km is already too big, in some sense, for the Geneva area... logistics in 20 years will be a nightmare given the foreseen increased population.A 1000 TeV pp collider is out of the question too due to synchrotron radiation. The critical energy would be in the MeV range, with loads in the kW/m... for FCC at 4.2 keV critical energy the load is at 30 W/m... and believe me, it's hard to design a machine coping with that already...

Those predictions would fill thousands of pages. Physicists have predicted signatures of supersymmetry and other non-standard model physics already for LEP 20 years ago. None of that came to pass. You don't have to dig deep to find the references.

I chose my words very carefully. Other experiments would more reliably offer new insights because in those cases we have good predictions or we already know that there is something which does not fit into the current theories. Most of those experiments are not more expensive (with the possible exception of building a telescope on the moon) than a new collider. Which of those would be the best, however, I cannot tell you.

That you expect me to come up with an assessment of all possible proposals in the foundations of physics is an obviously unrealistic expectation that likely you only brought up because you couldn't find any better argument. It does not work in your favor.

Mrs. Hossenfelder,aren't you still a "particle physicist" paid by me too? At least in the past, you were one.My diagnosis of your demand for a 90% reduction ("invented on the fly, referring to times in which no particle collider operates" - obviously, your dearest wish) is that of a frustrated person whose tenure is about to end.

I haven't worked in particle physics for a decade. That's easy to see from my publication list. Yes, I once worked in the field. That's why I know what I am talking about when I say their predictions are not to be trusted.

Yes, I am frustrated, but not for reasons that have anything to do with my job, which is going well, thank you. I am frustrated because we are wasting time and money on fruitless research.

Given the promise of plasma acceleration, it appears that a conventional circular accelerator like the one proposed might well turn out to be a complete white elephant, That would be a major embarrassment and waste of scarce funds better employed for other physics projects.

Like what??? 2-3 GeV over 10 m at awake experiment?... that's decades away from being usable in a machine giving luminosities comparable with those of LHC or FCC. Non luminosity no party... even at higher energies... it is that simple.

I'm glad to see agreement with the argument by Richter and others that serious efforts at new technologies now should come before any further expensive scale-up of the old ones. Perhaps resistance from the establishment would be reduced if you also proposed a substantial increase in funding to pursue those new technologies, which currently give off a backwater impression.

A commercial chirped-pulse FT microwave rotational spectrometer performing a published experiment[1] on a 3:1 enantiomer ratio pair of published molecules[2] plus one day: Validate or falsify Sakharov criteria[3] for baryogenesis. Validation sources Milgrom acceleration and in turn offers an empirical exception to the Equivalence Principe consistent with all prior observation in all venues at all scales. It also sources the cosmological constant [4] and removes SUSY's exact vacuum symmetry. Physics would be healed - for the cost of an LHC-week of coffee and donuts. Beauty? Man muss die Dinge nehmen, wie sie kommen.

Phillip wrote: In the grand scheme of things, the amount of money is peanuts. Probably more is spent on tattoos and piercings.

I'm surprised to see you offer this classic argument. It's used to justify all sorts of expensive projects, including pork barrel political projects. Including - I dare say - Trump's Great Wall project. I'll counter your classic argument with another classic argument:

Economics is the study of the allocation of scarce resources. We have infinite desires and limited resources to satisfy them. We therefore need to optimize the production from those scarce resources.

The question is whether a new collider, as described, is optimal for the world at this time. Even if we narrow our focus just to scientific progress, or narrow it further to progress in physics, is it optimal? Who gets to decide?

We need to do better than point out that the cost of colliders is smaller than what people spend on tattoos and piercings (or gourmet dog and cat food).

akidbelle wrote: Someone on the other side of the Atlantic wants 2 billions to build a wall … I really prefer a collider.

Unfortunately it doesn't work that way, so why even mention it? Most of us want the world to be run by smart, rational, reasonable, honest people, but for now that's a utopian fantasy. A new collider has to be justified on its merits, in the world we presently live in.

Frederic wrote: If particle physics is put "on pause" for 20 years, the skillset currently present in the community in building and running these massively complex experiments will disappear in the absence of a clear target.

I remember that's what people said about pausing manned Moon missions - we'd lose the skillset of Saturn V-level rocket scientists. Today, does anyone doubt that a new generation of rocket scientists can design and build vehicles for manned missions to Mars, if we decided to do that?

It was a mere seven years between the time Kennedy made his Moon speech and humans walking on the Moon, despite the immense complexity, expense, serious setbacks, political and social opposition, and no clear scientific goal. Yet here you are, worried that future scientists will struggle to build colliders even though they'll have tons of documentation on how to do it.

This call for a new collider seems akin to the moonshot of sixty years ago. That, too, was undertaken for political reasons (only it was the Russians who must be bested while now it is the Chinese.) The scientific rationale for the vast expenditure was never convincing -- we knew where the moon was and that it was made of rock. Then, too, we were told that there would be vast "spin-offs" of technology that would benefit all humankind but the only one most of us heard about was teflon-lined frying pans. In the end, the question was whether our captured German scientists were better than Russia's captured German scientists and on that rested shaky national prestige. As I recall, much of the politics behind CERN was also prestige -- this will demonstrate what we Europeans can do so up yours, Yanks!

If we could spend $100 billion to ascertain 1) that Dark Matter and Dark Energy actually exist, based on direct observation and/or 2) we discovered of what they were composed then the results would be a bargain at twice the price. But, are such specific experimental goals and procedures on offer here -- or it this more of desperation and giganticism on the part of some physicists, building contractors and politicians?

Remember the hype about "The God Particle?" Did the confirmation of the Higgs particle measure up to it?

Twenty-five years ago the Congress refused to fund the Supercollider. We were told by some that this was a scientific disaster for America. Has it been so -- or is America just ahead a few tens of billions of dollars for refusing to build the world's most expensive shotgun based on the rationale that if we do build it and shoot it aimlessly toward the sky often enough we will eventually bring down a target we didn't know was up there but is of inestimable value?

The moonshot was a complete waste of money because it had no legitimate scientific goal. It was just "Beat Russia" (now, China) and gee-whiz engineering.

As I understand it what is at issue here is not "Should we spent vast sums of money on achieving scientific understanding based on specific goals and methods?" but, rather, is the proposed collider the best means of doing this.

As a non-scientist I have no idea who is right. But, I am leery because of the similarly vague "benefits" promised from the politicized moonshot, its astronomical cost and the fact that it did not change human life, better or worse, one iota.

If CERN wants huge sums for a new collider it has only to promise it will lead to more effective weapons of destruction. Promise that and people will be passing the hat in their offices for it.

Sabine wrote: I am frustrated because we are wasting time and money on fruitless research.

I am frustrated that you apparently need to repeat this ad nauseam to people who just can't seem to get it. :-)

The sides that oppose you generally fall into three camps. One camp argues that, in the grand scheme of things, we're not wasting very much time and money. A variation on that theme is that the cost per person is pretty low.

Another camp argues that collider-based research is not fruitless, even if it doesn't live up to the marketing hype that sells it to politicians and the public. Variations on that theme argue that colliders might give us "tantalizing clues" and "unexpected surprises."

The third camp argues that the public needs to keep scientists employed and doing something in order to prevent the loss of scientists and valuable skillsets.

I haven't been in this blog very long, but long enough to notice these repeating themes. In my opinion, no one in this blog has presented a compelling argument against the points in Sabine's book.

I would find it interesting if someone who disagrees with Sabine's book would make a case against it chapter by chapter. It's a short, concise book, only ten chapters and only about twenty pages per chapter. Sabine would have the opportunity to respond, and the rest of us, at least those of us who have Sabine's book, could also participate. All we need is a worthy opponent who's willing to make their case. I think it would be tons of fun. This is Sabine's blog and it's her book, so let's do it! It's a rare pleasure to interact directly with an author.

I like your blog but I fear that recently your campaign against particle physics is starting to go a bit too far.Let me start with the costs. Let's take the most expensive version, 21 billions euros. In 2018 Germany's military spending alone has been of around ~ 40 billion euros. Double that much. Spent in 1 year, by one country (one that, btw, does not spend that much in military, proportionally to others). Let me also remind you that CERN has 22 member states, which all contribute proportionally to their GDP to CERN budget. On top of this, it is not only the member states that would pay for, work at and profit from an experiment like the FCC. To put things into perspective, the world's total military expenses are (according to wikipedia) around 1.5 *trillion* euros. So the "huge" costs of the FCC are just 1,5% of what the world spends in weapons and wars in 1 year!

Now on the physics part. Fundamental research works like this. We have ideas, propose things, maybe follow wrong leads and convince other people to follow them as well for years, to find only many years after, that we were wrong. This is all fine, it is how it works. True, we should try not to repeat always the same mistakes. While it is true that we don't know whether FCC or any other similar machine will find anything "new", I would like to remind you that the LHC has found already *new physics* and, given the present status, it will probably not be able till the end of its lifetime to tell us enough about what it has found.

The LHC has find a new scalar particle, which we call the Higgs boson. The fact that we expected it to be there, does not mean by far that we understand it. Being able to model something, even with very high precision, is very far from understanding what is really happening there. In particular, if our picture is correct, the Higgs boson is at the heart of a phenomenon of incredible importance: spontaneous symmetry breaking. And all that we have now is an almost high-school level model of it, with a phi^4 potential to model it which no one knows where it comes from. Now, if you are happy with having seen it, then good for you, but sorry if most of us particle physicists are not. Having just seen it at the LHC, without being able to measure how it couples to itself and to fermions does not tell us anything about whether our (simplified) picture is correct.

The SSB mechanism is such a fascinating phenomenon which appears at all levels in physics and the most fundamental of all these levels, the one that should explain how all particles acquire a mass, is the single one that we do not understand at all. I agree with you, it looks like old paradigms like naturalness have failed in guiding to understand what should be, but that's exactly why we need to measure it! With very high precision! And to do that, the LHC is simply not enough. Now this reason alone would be more than enough for me to spend 1% of the world's yearly military budget for a project which would have a lifetime of decades, would stimulate incredible technological advances and would also have an impossible to foresee discovery opportunities. Yes, impossible to foresee, because it's new territory and no one really knows, even if we like to convince ourselves that we do, in one direction or in the other.

So I think, as a scientist, it is really bad to keep on talking about money, amplifying even more the perception of the public on how "shamefully" expensive this machine would be. There are much larger expenses that we should be ashamed of. This is more than justified. If we believe that there are other (similarly expensive) experiments that should be built (I think of LISA for example), let's start fighting for those ones, with data, numbers and physics cases built on calculations, and let's have them built as well, if we can. Fighting against each other will just lead us to nothing. This is how I see it at least.

In Erwin's universe, it makes perfect sense that physicists with tenure would never question the value of new colliders or any other expensive projects. Only physicists without tenure would question such things.

Neutrino physics has a lot that we can sure to measure (neutrino masses, CP violation, etc). While DUNE is going forward (~2b USD) it won't answer everything. I think it might just be that particle physics needs to go away from bigger and bigger e/proton colliders and go to specialized colliders (mono-energetic neutrino beams). Particle physics doesn't need a break, just a different orientation.

Perhaps you would enjoy participating in the presentation ofFCC CDR at CERN 4-5 March, c.f. the open invitation attached below. You are certainly very welcome!

I agree with you that there is no no-lose theorem that assures a discovery of something new at this facility. Does that then mean we should simply give in? Postponing a decision by 20 years will certainly assure that CERN will no longer exist.A new start will then be very difficult. The current thinking isto first install a very high-luminosity electron-positron collider in the 100 km tunnel. This will provide extremely precise consistency tests of the Standard Model and searches for rare phenomena like lepton flavour violation and/or righ-handed neutrinos. You can think of this as an intensity frontier experiment. Then after 15 years of e+e- operation starting in 2039, a proton-proton collider could be installed in the tunnel if mankind still finds this worthwhile. This combinedprogramme leaves considerably more than the 20 years you ask for for the development of new magnet technologies. And possibly one would be able to reach considerably larger energies than the 100 TeV mentioned.Best,-Mogens

By the way, the dramatic music in the marketing video is a subliminal message promising what a new collider can do.

Even though I'm completely aware of the music and its manipulative purpose, I can't help but feel excited about a new collider. The video also contains a lot of sound bites designed to manipulate. Being aware of manipulation - whatever form it takes - is necessary to guard against its effects. Sometimes we want to be manipulated, such as when our partner seduces us. :-)

I watched a film last night, The Natural starring Robert Redford. A woman was talking to Redford about allowing herself to be manipulated for the sake of material benefits - an old story between men and women. She asked Redford if he thought there was anything wrong with that, and he said, "Not if you understand the risks." I was struck by the simplicity of this profound insight. I have a bad habit of finding profound insights in popular entertainment.

"It is OTHER people's money, that we seem to be willing to spend with no good direction, and I think that is worth keeping in mind. The average taxpayer is the one that foots the bill."

I agree completely. HEP has become ever more remote from the rest of science, and any potential applications. It is strange that the search for the fundamental building blocks of matter has (hopefully) ended this way, but that is the way the cookie has crumbled!

The only reason this expenditure of public money is tolerated, is because too few people realise how irrelevant this research is to everything they really care about.

The Intel example is a good one, but perhaps not in the way you're thinking.

I have long suspected that tech companies like Intel (Apple also comes to mind) have more than one future generation of products ready for production at any given time.

But the goal is to "dole out" incremental increases in performance every six months in order to maximize profit.

Computer "gamers" are one of the easiest targets for this tactic. They will, every six months, shell out more than they can afford for the "latest, greatest" graphics card. Four months later, the "gamers" are pawning their cards for a fraction of the original cost, in order to buy food. Two months later, an incrementally-better card comes out, and the cycle repeats (this is how I get kick-butt graphics cards for pennies on the dollar : )

So the Intel example is appropriate; just replace "Intel" with "physicists", and "gamers" with "uninformed public" to see who is being played.

I find that I can end up with a blazing-fast computer system for minimal expenditure by playing this cycle. Just extrapolate that alone to the collider equation. In many cases, the cost of technological equipment goes down over time as performance increases, so, why rush?

I dare to point this out because I'm not a physicist... or IC designer. Dr. Bee certainly cannot be doing so for selfish or ill-considered reasons.

A couple of months ago, I watched videos detailing the birth of the "internet" at DARPA, as well as the advances in 20th-century physics. Notably absent were the Chinese... "Where were they?", I asked. "Learning to steal" is probably the shortest answer.

If building the new collider in Europe will prevent its being built in China, I would personally donate to see that happen. The worst outcome is that any future advancements occur in China. Never forget:

My view is we have only so much money to invest in research, therefore it should be viewed competitively. People who say ten billion euros is "not much" seem to have a different view of "much" to me. The only reason I can see why this could be viewed as plausible is that since everybody seems to think there is nothing to find there, you fund it to prove them wrong. The trouble is, they could be right. The next thing to consider is they want to go from 14 TeV to 100 TeV, which is a bit over a factor of 7. Why is it thought that is big enough to do something dramatically different? What problem would it solve, how and why? My view is, until these sort of questions get sound answers, delay is fine.

Another question is, could anything more be done with what is there? Suppose dark matter was actually rather light and within the current energy limits, how would you detect it? Given we are probably looking at fairly standard detection systems that would not detect dark matter, so just maybe a little thinking might not go astray there?

Dear Sabine, your good intentions and careful choice of words are much appreciated.

You wrote: "Other experiments would more reliably offer new insights because in those cases we have good predictions or we already know that there is something which does not fit into the current theories."

This would be exciting. See, I'd love to read a factual research publication, rather than a blog summary, that supports this statement. It does not require to evaluate all possible proposals -- only the ideas that trigger interest from a stratum of informed experts. Can you recommend such a publication? Thank you.

It is clear from your comment that you do not understand what I am talking about when I say the predictions for new physics are not based on sound arguments, in contrast to the prediction of the Higgs. I recommend you read my book.

"So I think, as a scientist, it is really bad to keep on talking about money, amplifying even more the perception of the public on how "shamefully" expensive this machine would be."

As I have pointed out many times, I do have very concrete recommendations and alternatives, that come with proposals in any length from one paragraph to 20 pages. Your complaint that I supposedly don't merely shows you didn't bother to even find out what I am saying to begin with. It is both stupid and wrong, and, as I already mentioned here, exceedingly unoriginal in addition.

I wish there was one, but unfortunately there isn't. Even more unfortunate is that I don't think there ever will be one. The community is too fragmented. Everybody is merely banging their own drum, hoping that who bangs the loudest gets the money. They have no reason to sit together and figure out what's the best avenue to continue. And, as I said, it's not a task that one person can do in their free time.

Two fields of science 'eat up' limited science funding...manned space flight and ever larger particle accelerators. Neither deliver on promises and neither can justify their share of research dollars.

Also, we are underestimating the imminent role that AI is about to play in expanding our knowledge of the Universe. I'm with those 'tech geeks' who see the future discoveries of physics not coming out of Berkeley and Cambridge but rather out of Apple, Google and their Chinese equivalents. AI will be an existential tool to expand knowledge...the equivalent of the Nuclear bomb in WW2. In 20 years, 200 million teens in their bedrooms are each going to have access to more computing power and tools than the top physics institutions have today.

I remember that's what people said about pausing manned Moon missions - we'd lose the skillset of Saturn V-level rocket scientists. Today, does anyone doubt that a new generation of rocket scientists can design and build vehicles for manned missions to Mars, if we decided to do that?

We did lose some of that skillset. People sometimes ask whether it makes sense to design expensive new heavy-lift rockets like NASA's Space Launch System -- why not just make new Saturn Vs? In 1975, it would have been relatively simple to build new Saturn V rockets. Today, no one knows how to make them because the people who did -- including those with critical knowledge that was never properly documented in the rush to finish Apollo -- are all retired or dead. So instead we have people having to create new Saturn-V-class launchers from scratch.

And, of course, billions of dollars were spent on the Space Shuttle as a follow-on of sorts to Apollo, which helped maintain and advance some of the non-Saturn-V-specific skillset. The real comparison is probably not to "pausing manned Moon missions", it's to "not building any more rockets after Apollo".

Of course, we can recreate this knowledge ("a new generation of rocket scientists can design and build vehicles"). It's a question of how much unnecessary wheel re-invention would need to be done in that case.

@ R. TaylorI have long suspected that tech companies like Intel (Apple also comes to mind) have more than one future generation of products ready for production at any given time.

Then why has Intel kept delaying its advances (e.g., moves to smaller-scale manufacturing processes)? Why has Moore's Law basically failed in the last few years?

I find that I can end up with a blazing-fast computer system for minimal expenditure by playing this cycle. Just extrapolate that alone to the collider equation. In many cases, the cost of technological equipment goes down over time as performance increases, so, why rush?

For some technologies. For others, no. (Look how expensive and time-consuming it's become to produce new iterations in airplane design for only incremental improvements in performance, compared with what was going on up until the 1970s.) Since particle accelerators are not mass-produced, manufactured items, they cannot take advantage of increasing economies of scale or competitions between different producers, so they're much less likely to see costs behave the way mass-produced consumer items (sometimes) do.

And you clearly haven't been looking at computer performance in the last few years.

I dare to point this out because I'm not a physicist... or IC designer.

Translation: "I dare to point this out because I have no idea what I'm talking about."

I suspect that the best place to spend a few tens of euros on physics would be building big telescopes (optical and radio) on the Moon's far side. These could potentially clarify the two biggest puzzles in physics today, dark energy and dark matter.

Regarding: "i know this is going to cost more, but why not make it 200TEV or even 1000 TEV?"

Answer: There isn't enough physical space in the Geneva area to build this. The FCC report assumes 1 TeV per 1 km of ring (about right, given where we expect accelerators to be). It needs to be built on a single geographic plate. (and FCC will fill most of the Geneva basin). Building it elsewhere may be possible, but without major advances in accelerator technology, it won't be possible to do higher in the Geneva area.

Regarding: "I would find it interesting if someone who disagrees with Sabine's book would make a case against it chapter by chapter."

Answer: Sabine's book entirely, critically, and wrongly assumes that experimental particle physics is wrapped up in and dependent on the personal artistic and philosophical expressions of a handful of SUSY-die-hard theorists. It's a straw-person argument, so it's easy to refute: Experimental particle physics has extensive success, even if Sabine doesn't find it personally interesting. WE UNDERSTAND NATURE AT 10^-20 METERS. That is, in and of itself, a monumental feat for humans, because up until 2012, we *DID NOT KNOW THAT*. The Higgs boson is actually extremely surprising. Spin-zero particles do not play nicely with QM. It's a "spherical cow" solution (https://en.wikipedia.org/wiki/Spherical_cow). The surprise of seeing a spherical cow actually in nature cannot be understated. We need to understand what the hell this thing is, and we frankly don't.

Regarding various interpretations of "25B Euros is a lot of money, spend it on something else": We do. On national scales, this is a pittance. NASA spends about that much *per year*. I love NASA, but really, a new collider is a bargain compared to, say, looking at rocks from Mars (which, don't get me wrong... is actually really fascinating and interesting) and will vastly expand our understanding of the universe.

Regarding: "8x the energy is not much": If you don't think a factor of 8 is that much, do you mind giving me 7/8ths of your salary and you can keep the remaining 1/8th?

Hello there. Care to tell us who you are? I am guessing a particle physicist who doesn't like that I am not banging the drum for the a bigger collider?

"Sabine's book entirely, critically, and wrongly assumes that experimental particle physics is wrapped up in and dependent on the personal artistic and philosophical expressions of a handful of SUSY-die-hard theorists."

I assume no such thing. My book is very explicitly about theory-development. It is not even about particle physics in particular.

Ah, more false accusations. None of the arguments in my blogpost are based on my personal interest. I have laid out very clearly why I think a larger particle collider is at the current time not a good experiment to invest in.

The only argument that you have come up with in return are personal attacks. And not only this, but personal attacks hidden behind a pseudonym. That illustrates the quality of discussion in particle physics very nicely.

Peter Erwin said Look how expensive and time-consuming it's become to produce new iterations in airplane design for only incremental improvements in performance, compared with what was going on up until the 1970s. Experimental particle physics might be similarly compared. Fermilab from the old machine through the tevatron produced a lot of physics from the 100GeV to 1.5TeV range. Then the LHC we have essentially only the Higgs particle to crow about. With this next generation we may have not much. Theory has indicated there is a sort of QFT “dessert” from 10TeV up to the GUT scale or so, and we may find this is the case. Well texperimental data in this regime will tell us something, so it would be of some value.

In the end you are throwing €9 billion (and of course it will be larger as these things always are) and even if we get SUSY out of this that is a lot of money spent on a small piece of knowledge. It is today's version of the critique of spending the equivalent in today's money of $200 billion to get a few hundred pounds of moon rocks. No matter how you try to put this you have PR problem. It also might mean we are reaching some sort of possible limit. We are also many orders of magnitude down from any scale of unification and from quantum gravity. We are just scratching the surface.

Maybe the case for this larger collider is in the end reasonable, but even if this is built I suspect it will be last of its sort. I think we might consider thinking anew about things. The collision of black holes is a scattering of black branes or large N modes of quantum Planck units and the signatures of quantum hair may exist in gravitational radiation. With more advanced and space based interferometers we might start to find BMS or related quantum information imprinted on spacetime. I also think structures at one scale in nature often reoccur at others, and so information from other areas of physics may be brought to bear as well.

When a certain trend in developments is starting to play itself out we can either look at this as a disaster leading to some dark age, or we can look at it as an opportunity to rethink and do things differently.

Are you seriously accusing Sal of hiding behind pseudonym when he signed his comment with his last name?

If you are getting annoyed reactions to your posts, it is because you also keep misrepresenting over and over again the physics case for a future collider. I understand that you don't think precision measurements of the Higgs sector and the study of electroweak symmetry breaking phenomena are worth the construction of a larger experiment, but people can and do strongly disagree with that opinion.

Given that a search for "Rappoccio physics" turns up exactly one name involved with the LHC, it's not a pseudonym ;)Anyway, it never ceases to amaze me when even people who should know better steep to ad hominem attacks. The very nature of being a scientist is sticking to FACTS (pardon the emphasis). Now, while a certain bias is certainly only human and Sabine sure isn't completely free of it (and neither am I nor anyone else), the book in question is nothing if not objective. The only subjective parts are the things the people interviewed say, but that's clearly not the author's fault. Kudos btw. for letting those comments through and responding. Don Quixote would be proud ;)

Who is Sal? Are you trying to tell me that the commenter with the name "rappocio" has a first name "Sal"? And you come here to complain that I don't know this? Then you wonder why I am annoyed about the nonsense I have to deal with?

"If you are getting annoyed reactions to your posts, it is because you also keep misrepresenting over and over again the physics case for a future collider. I understand that you don't think precision measurements of the Higgs sector and the study of electroweak symmetry breaking phenomena are worth the construction of a larger experiment, but people can and do strongly disagree with that opinion."

I was the one who correctly represented the case by pointing out that more SM measurements is the only thing a larger collider will reliably do. You only have to read what I wrote to see that.

It does not remotely surprise me that particle physicists are annoyed. Doesn't change anything about the facts though.

Thanks for pointing out that "Rappoccio" is a family name and not a type of noodle. I apologize for not knowing this. Turns out though I was guessing correctly that we have here yet another particle physicist.

The incremental SKA (square kilometer array) here on Earth is likely to do the DE job far better. And the JWST and a couple of Hubble replacements/extensions be better than far side optical/UV/IR telescopes for both DE and DM. Not to mention the LSST, with a fleet of ground based telescopes to do the spectroscopy. Of these, only Hubble replacements/extensions are as yet not already well advanced.

Further to my CIP/far side comment: useful for DE (as Sabine notes, far side telescopes, of a few billion euros, would likely do little for DM) telescopes would surely cost vastly more than a few billion euros. There’s the whole space communications infrastructure to build and maintain, for decades (there are no stable Moon orbits, for example, to put a fleet of comsats into), once you’ve got a versatile array of radio scopes built ( how would you maintain them?). And what sort of optical scopes would you build anyway?

"Answer: There isn't enough physical space in the Geneva area to build this. The FCC report assumes 1 TeV per 1 km of ring (about right, given where we expect accelerators to be). It needs to be built on a single geographic plate. (and FCC will fill most of the Geneva basin). "

ok, what about China building a 200km ring, or even larger. another piece of dat

"Regarding: "8x the energy is not much": If you don't think a factor of 8 is that much, do you mind giving me 7/8ths of your salary and you can keep the remaining 1/8th?"

what about the latest results of ACME no EDM down to 10-29

my interpretation of ACME is that new physics is seemingly unlikely at 100km, 100TEV, so why bother with a 100km tunnel at least CP violating physics. esp split SUSY naive SUSY and SO(10) GUT

since ACME seemingly suggests no new physics at 100TEV, perhaps the goal should be much higher, 200TEV or even 10000TEV

for China, how much more expensive is digging then operating a 200km tunnel or even 1000km tunnel over 100km?

This constrains some new physics models, and not others (just like every other search). You can see here for a nice overview paper. To evade these bounds, one only has to dial down the coupling of new physics to electrons.

for China, how much more expensive is digging then operating a 200km tunnel or even 1000km tunnel over 100km?

Costs would mostly scale accordingly. However, I'm not so sure many people will be comfortable doing science in a nation that is actively engaged in ethnic cleansing of the Uigher population. I certainly am not.

What do you think about big pots of money for new/extended experimental work on neutrinos? Both “lab” and “astronomical”. Like IceCube variants, very wide field, very low incidence things like radio signatures from the Moon (would include UHECRs), and deeper searches for supernova, blazer, and compact mergers (e.g. NS-NS, NS-WD, NS-BH) signals? Of course, some of these have bonuses like testing Lorenz invariance ...

Taylor wrote: I have long suspected that tech companies like Intel (Apple also comes to mind) have more than one future generation of products ready for production at any given time. But the goal is to "dole out" incremental increases in performance every six months in order to maximize profit.

Is there any evidence for your suspicions?

Let's clarify what you're saying. Let's say that customers currently have version 2.0 of an Apple product. You're saying that Apple has version 5.0, completely tested and ready to go, but instead of releasing version 5.0 to the public, they "dole out" versions 3.0 and 4.0 in order to maximize profits. Apple is doing this even though version 5.0 would blow the socks off of the competition. Or maybe you think that all the companies are colluding with each other to dole out incremental improvements, so no product is clearly superior?

Don't get me wrong. I don't think corporations are saints and I know some of them will do just about anything to maximize profits. As the saying goes, some CEO's would swindle their own grandmother out of their retirement money. It's also been said that psychopaths make good CEO's. :-)

Peter wrote: Today, no one knows how to make [Saturn V rockets] because the people who did -- including those with critical knowledge that was never properly documented in the rush to finish Apollo -- are all retired or dead.

In my career as an engineer, some of my biggest battles with management have been about taking the time to properly document what we were designing. I'm sorry to say that I never won a single battle. I guess they don't teach documentation in business school.

Regarding Apollo, if they had taken the time for proper documentation it would have been 1970 instead of 1969? But Kennedy said it had to be done before the end of the decade, so what choice did we have? Apparently Trump's Great Wall has to be built before the end of this decade. If we adopt a sexagesimal calendar system, maybe that would help us set more realistic timeframes for massive projects.

Peter wrote: So instead we have people having to create new Saturn-V-class launchers from scratch.

Yes, if we decide it's important to send people to the Moon and Mars. But if we decide to do that, we'd better have some long-term goals. It would be a shame to lose all those skillsets all over again.

If we want to spend tons of money on fun space projects, I'd prefer that we build a space station like the one in the movie 2001: A Space Odyssey. You know the one I'm talking about. And if people pay to visit the space station, maybe it could pay for itself. Or, instead of HAL, we could have Amazon, Apple and Google compete to install Alexa, Siri or Assistant. That alone might pay for it.

Alexa, Siri and Assistant would never say, "I'm sorry Dave, I'm afraid I can't do that." This is how it would go:

Dave: Siri, open the pod bay doors, please.Siri: Sorry, I didn't quite get that.Dave (more slowly): Open the pod bay doors.Siri: Sorry, can you say that again?Dave (shouting): Open the pod bay doors!Siri: Sorry, I can't find that.

At that point Dave decides to enter through the emergency airlock. Later he finds out that Siri was mad at him for mistakenly calling her Alexa.

Rappoccio wrote: Sabine's book entirely, critically, and wrongly assumes that experimental particle physics is wrapped up in and dependent on the personal artistic and philosophical expressions of a handful of SUSY-die-hard theorists. It's a straw-person argument, so it's easy to refute.

Have you read the book? If you think it's easy to refute, would you consider refuting it chapter by chapter, here in this blog? Some of us have Sabine's book.

Bahle wrote: Anyway, it never ceases to amaze me when even people who should know better steep to ad hominem attacks.

I'll say. Did you happen to see Roberto Kersevan's (CERN) comments in the previous discussion about a new collider? I'd have trouble distinguishing him from a troll. I'm surprised by scientists who think ad hominem is an effective or appropriate strategy.

SH wrote "Your complaint that I supposedly don't merely shows you didn't bother to even find out what I am saying to begin with. It is both stupid and wrong, and, as I already mentioned here, exceedingly unoriginal in addition."

sorry for .. lacking in originality. :-)

I clipped the following from the referenced post.

"First, it’s a stupid criticism that tells you more about the person criticizing than the person being criticized. Consider I was criticizing not a group of physicists, but a group of architects. If I inform the public that those architects spent 40 years building houses that all fell to pieces, why is it my task to come up with a better way to build houses?"

as I see it, building one house which does not fall apart would allow the public to judge for themselves. without, even though true perhaps, all the public sees is conflicting opinion. and your "task" (burden?) because you chose to denounce the .. poor practice.

(if I were a physicist, I'd have tried for a better analogy, so, another "sorry", in advance).

I believe god exists in an elusive fundamental particle that may be discoverable at a collision energy of 20 TeV or much, much greater... I’m requesting €21 billion (I won’t kid you with the €9 billion estimate, these things always cost at least double or triple those initial estimates), for a collider that may detect this particle. If we fail due the particle not existing at all, or because we need much higher collision energies, at least we will have proven conclusively god doesn’t exist in a particle at energies below 100 TeV. This alone would be a great advancement in scientific knowledge and for Human kind well worth a €21 billion investment!

My contention that Intel has more than one future generation of products ready for production at any given time implies precisely that they are delaying moves to smaller-scale manufacturing processes.

The why, I believe, is in part to maximize profit (which I don't hold against them) by taking advantage of those who believe that, when a 3.2GHz processor is introduced, they must discard their nearly-new 3.1 GHz system, whether based on peer pressure, bragging rights, or whatever motivates them.

You go on to ask:

"Why has Moore's Law basically failed in the last few years?"

So you are now asking me, the uneducated one, why a bunch of highly-trained computer scientists were parroting the same belief which turned out to be wrong? (crickets)

I said:

"In many cases, the cost of technological equipment goes down over time as performance increases, so, why rush?"

You responded:

"For some technologies. For others, no."

Look, I hated English courses. But I have always scored in the 99th percentile in reading comprehension assessments. I know for a fact that you can replace the "In many cases" in my statement with the "For some technologies. For others, no." from your response without changing the meaning of my original assertion! Again, you apparently try to contest my position by agreeing with it.

You state:

"And you clearly haven't been looking at computer performance in the last few years.

Actually, that is precisely what I have spent the most of my time "looking at" over that time frame. Below, I've listed three examples that bolster my original contention regarding the incremental increases in processor performance; I could provide 1,000 similar examples. The format is Processor Model Number / Frequency / Release Date.

Core i5-2300 / 2.8GHz / January 2011

Core i5-2310 / 2.9GHz / May 2011

Core i5-2320 / 3.0GHz / September 2011

I completed an A.S. degree in Networking Services in mid-2013. One of my professors, who, among other qualifications, held a degree in journalism, marked a passage I wrote in a paper titled Defense In Depth for my Network Defense and Countermeasures course with the following comment:

"Have you considered pursuing a PhD?

I responded: "Shouldn't I finish my A.S. first?" : )

In the interest of brevity, I will stop here. But you may want to do us the favor of listing the things that you don't know.

what do you think of the proposed Japan linear collider, articles say price tag $10 billion, to study higgs?

rappoccio

politics aside, if Cern with proposed FCC and China with its proposed collider were to combine resources, perhaps a 200km 200TEV collider could be built, in china of course. building 2 100km 100TEV colliders sounds like a waste in comparison to 1 200km 200TEV collider.

there are news articles which state China plans to start digging as early as 2022, of course the texas scsc was cancelled

In context, your argument devalues pure research: Because we want to seek out knowledge. Research for research sake. Is it all a matter of money, or is there something more?

Negative results are data, too. There is no guarantee a new particle / field will be discovered, but so what? Nobody knows until it is attempted.

Outside of physics, if there was "no good reason" to study genetic variation in amoebas, would you still stick to your argument? Does it matter whether it cost $50k or $1mil? Does it depend on who pays for it? Do we have to know a priori that amoebas might hold the key to tissue regeneration, or, can we just want to know?

Your answer to my comment does not answer any of the points I raised. So let's forget about that and let me try again, because somehow you keep on ignoring one important point.

What some of us are trying to say is just that, even if there is a part of the community that has carried on going in a direction that didn't bring results (hierarchy problem, naturalness and all that), this is not a reason to attack blindly the whole theoretical particle physics community which is made of people doing all possible things from precision studies in QCD/EW theory, to developing new observables which enhance sensitivity to any kind of physics, to study non-perturbative aspects of QCD, all the way to the mathematical foundations of QFT, the special functions that appear in perturbative QFT and what not.

All these people's work draws from collider physics, depend on it and at the same time made possible all physics studies that have been made at the LHC, at LEP before, and will hopefully be made at the FCC. For how the situation stands now, this is the most serious chance we have to understand a bit of what is going on in the Higgs sector of the SM, for real, without having to resort to the "beauty arguments" that you don't like. I don't like them either.

So why do you keep on confusing *a part* of the community (which is well entitled to speak for itself) with the whole particle physics community which wants to build the FCC because of thousands of reasons that have nothing to do with what you fight against? If you don't agree with these reasons (the real ones, not the naturalness blabla), it's ok, we can discuss about this. But as it stands, in my opinion you are missing the whole point.

I am on the fence when it comes to this 100TeV machine. I can see pros and cons either way.

A sports analogy might be in order. You have individual sports such as track and field. Then there are small team sports such as basketball. One thing that is nice about basketball is you can actually play basketball. Then you have American football, which is a completely industrial mass-scale sport that few can play. The NFL teams are multibillion $ corporations and the industry has mass coordination of many thousands of people. Few of us can really play it, that is unless you like frequent visits to a trauma center. Particle physics is analogous to football. It is a hugely expensive enterprise, with the case of the LHC we have only the Higgs particle to claim.

The PR problem remains even if you point out money spent on tatoos. I never got one and have little interest in such, yet people who get them are fueling their vanity. The average person has really no idea what the Higgs field is, what Goldstone bosons are and what is this Higgs particle anyway? Most people really do not care that much, but they might like showing off their latest tat-job. A friend of mine from high school is 100% covered with them.

I double down my statements when it comes to manned spaceflight. I wont go in depth, but these ideas of putting people on Mars with no clear reason for it are the height of technological insanity.

Of course much of science is expensive these days. Anything involving space science costs around $5000/kg to place in orbit with a times 2 or more if you go beyond. A space based gravitational wave interferometer will not be cheap, but I suspect it may inform us far more about the foundations of the cosmos. We may learn a thing or two about quantum gravity. For particle physics at the 10^2 to 10^6TeV energy there are cosmic rays, and the system lofted over Antarctica is making some interesting finds. Sure cosmic rays are not controlled, they are not prepared states, the scattered daughter products are in a narrow cone and statistics are generally lousy. These might have to be worn with persistence and patience.

Rappoccio wrote: I'm not so sure many people will be comfortable doing science in a nation that is actively engaged in ethnic cleansing of the Uigher population.

I could ask if you think all the democratic nations should completely shun China - assuming such a political consensus was possible. Or does your shunning only go as far as colliders?

But this is a science blog so I won't ask. My rhetorical question is a sufficient response to your deeply considered remark. However, I'll give you some bad news: American and Chinese scientists already work together. American scientists work in China; Chinese scientists work in the US. (not just the US, of course) Several years ago Chinese scientists began producing more scientific publications than American scientists. Should we ignore each other? (another rhetorical question)

You don't need to be an architect to notice that a house falls to pieces, and you do not need to be a physicist to see that the predictions which theorists have made for the past 30 years were, de facto, wrong and have all been ruled out. Most people have no trouble seeing that that's a fact, not my "opinion", as you erroneously state.

First let me mention that I explain all of this in great detail in my book.

The brief summary is this: In the foundations of physics it has become very difficult to test new hypotheses. It takes a lot of time and a lot of money. We cannot make all experiments we want, so we have to be very careful when we decide which hypotheses to even put to test.

A null-result is also a result, but if you want to develop a new theory it is not a very useful result. What you need to guide theory-development is evidence for some new phenonemon that you can built into a new theory. All that null-results do is tell you that the previous direction wasn't the right one. And even that limited use of null-results turns to no use if you do not learn from null-results. We have seen null-results for 30 years, but all that theoretical physicists have "learned" from that is to construct theories that are, for all practical purposes, unfalsifiable.

The conclusion I draw in my book (I cannot summarize the whole argument here) is that we should focus on cases where we know theory is in conflict with data, or the theory has an internal inconsistency. The standard model as it is is fine all the way up to the Planck scale. Hence, there is no reason to think the FCC will tell us anything else than a next digit on some standard model parameters.

For this reason I say we would be better off first finding out more details about dark matter, dark energy, doing more high-precision measurements, doing some small to medium scale experiments probing quantum gravity and quantum foundations. And waiting for theorists to come up with better predictions. After that, we can revisit highly energetic particle collisions, should it turn out that we expect something to find there.

I have said this many times before, but particle physicists seem very slow in understanding. The part of the community that I am talking about is the part that draws attention to your discipline. It's the justification of your existence.

I am perfectly aware that there are theorists doing other things and that experimentalists have their own interests and so on. But who cares? You all sit in the same boat, and you know it. You have profited from those theorists' wild predictions that capture the public attention, you have not uttered a word of disagreement, and now you will go down with them.

Those theoretical physicists with their big and fancy predictions were useful as long as they brought you money. Now that it turns out they were wrong and their reputation is damaged, you want nothing to do with them. That will not work. We cannot trust the predictions of your community. That's a big problem and you should fix it. Until this happens, funding a next larger experiment would be a waste of money. Best,

From how you write, you clearly don't want to discuss seriously, neither have any idea of most of the particle physics community that I work with and represent, what we are trying to do and how we talk about it with the public.

Something does not become true only because you state it over and over again, even if you wrote a book about it. But apparently, the only thing you want to do is sell your book. Fair enough, it is your right, but I wonder where is the difference between you and anyone else selling their ideas *at any cost* for 30 years?

She just want to sell her book. So writing 90% of particles physics (physicists) is useless is part of a commercial strategy (provoking, polarising, attracting anyhow attention). The arguments in the book can be at least partially sound, but disqualifying an entire field of science is a way of discussing I am not getting into. Regards

Ah, let us see. Here we have the ultimate "argument" that I get from particle physicist: Supposedly I am just trying to sell a book. Interestingly, you make that argument in one breath with accusing me to be the one who does not want to seriously discuss the matter. Figure that.

How about not making personal attacks on me and instead sticking with the point? Has that occurred to you? Am I asking for too much? It surely seems so.

I am really sorry, but what you write about naturalness problems, in particular the presumed differencebetween the KKbar mass difference problem (solved by placing the charmed quark at around 1 GeV)and the electroweak mass problem shows you have not thought well enough about these issues.I suggest to spend more time while thinking than while writing. Turn electricity off...it helps!

Oh, really? I am so sorry for being dumb. How about you enlighten us? Please tell us just how naturalness arguments lead us to conclude that new physics should appear at the TeV scale. And while you are at it, please also explain why that hasn't happened.

I found this interesting: obviously, it is only snapshots and not the official CERN line, but it is CERN people speaking. It seems there is a bit of "revisionist history" going on ;)

tl;dr in advance: 7 years ago: we will find tons of stuff with the LHC. 3 weeks ago: we built the LHC primarily to find the Higgs, mission accomplished, astounding success

7 years ago (Pauline Gagnon)Did we build the LHC just to find the Higgs? There are bozos and bosons, and if the Large Hadron Collider (LHC) were built only to find the Higgs boson, you would be absolutely right to think all physicists belong to the first category. But the fact is, the LHC does much more than search for Higgs bosons. (https://www.quantumdiaries.org/2011/10/03/did-we-build-the-lhc-just-to-find-the-higgs/)

three weeks ago (Tommaso Dorigo)But that argument [new physics at TeV based on naturalness], I claim, is unnecessary (and in fact, it was not the reason for building the LHC in the first place, as the LHC was primarily built with the goal of finding the Higgs, like it or not). (https://www.science20.com/tommaso_dorigo/why_we_need_a_new_collider-2359409)

You may not like my name, it's ok, even though the discussion is not exactly about that...."who knows everything better", this is also is common, turning your bad attitudes against interlocutor.Good luck for your book.

Just to cool down the discussion (you are ramping-up straight into the high-energy regime).

I have just found this:

http://faculty.poly.edu/~jbain/papers/Naturalness.pdf

and the 1st thing I thought was : What would Sabine say about that? (it is likely you know it already as you are cited there, apparently the author seems to be inclined to the mentioned arguents of yours)

So maybe at least his line of reasoning would be a pretty neat argument for naturalness (and only naturalness per se, not for any new LHC ;) )

I do not know what makes you think I dislike your name. This is not so. I merely point out the obvious, namely that you do know what we are even talking about, have no argument to offer, and - as usual - are too much of a coward to sign your nonsense with your name.

Thanks for the link to the pdf which I had not seen before. I looked at it and the argument sounds familiar, which made me recall that I heard a talk by the author last year (pdf here). I cannot now recall the details, but I believe I largely agreed with his argument.

Thank you, this presentation is in turn something I havn't seen before

BTW, I am interested mainly in his views about radical ontic structural realism (and this is inspired partly by your post about thinking electrons ;) - at least this is how I found him (or rediscovered)

What Intel does is actually very well documented (on a high level, at least; there are lots of trade secrets in the details). They do work on two generations of processors simultaneously. One reason is, of course, to roll out chips with greater frequency. But it also turns out that this isn't so wasteful on their part; there are two kinds of advances you can make in chips. One: clock speed and two: architecture. So the first team produces a new chip that improves clock speed but uses more or less the same architecture. Then the second team produces a chip that keeps the same clock speed, but updates the architecture to take advantage of this improved clock speed. You have two teams with different skill sets, and if they were all working on the same chip simultaneously, they might get in each other's way.

And the reason that Moore's law is running out is physics, and nothing to do with intel's development cycle. The processor speed seems to be bumping against the hard physical limits. There is some absolute limit to processor speed, and the closer you get to that the harder it is to make any improvements. We started out very far away from these limits, which is why we had 40 years of exponential increase in chip speed. And now we're nearing them, so advances in clock speed are taking longer than they did previously. Intel currently promises to have the next generation in clock speed advance out this year, delayed by a year, but there aren't going to be very many more generations; in the future, improvements in performance is mainly going to be driven by architecture in the future.

CrCl3 dissolves in water, 585 g/L. Wow. Put one gram in a liter of water in a 2 liter flask, add a vertical condenser, reflux open to air. A year later, a gram of lavender powder still decorates boiling water. Ten liters of boiling water? No! Cool. Add a dust mote of metallic zinc. DISSOLVED! There's a footnote (Nobel Laureate Henry Taube).

@Peter Shor: Good analysis. Another tidbit: When back in the 1990s RISC (reduced-- instruction-set computer) took over from CISC (complex--instruction-set computer), many thought that RISC was inherently better than CISC---hey, they are faster, right? Yes, RISC processors bought at a certain time were faster than CISC processors bought at the same time. But actually, CISC processors are better. The reason RISC is faster is because they are simpler, so the time from design to market offering is shorter, which means that the design was started not so long ago, after some substantial progress due to Moore's Law since the time farther back in the past when the CISC design was started. Once Moore's Law begins to peter out, we might see a return to CISC.

The argument that we can access 'new knowledge' by building a larger collider doesn't really work because it ignores the question of the relevance of that knowledge to anything that anyone - even other scientists - cares about.

For example, there are people who are dedicated to finding ever more digits of pi. They are constantly generating more knowledge, but would anyone suggest that we should spend $20 Billion to obtain such knowledge?

In the end, it will cost less than two nuclear aircraft carriers! This means, about US$ 2.50 per person on Earth during the whole upgrade. So, it is globally a quite cheap and worthy enterprise, which also leads to better integration of smart people worldwide. There are still important high-precision measurements of SM that would be done at ILC, whether it was to be built, but surely they will happen in the new e-e+ accelerator at CERN. For instance, measuring the Higgs and Top mass more accurately may establish if thr SM is metastable (or even stable) up to Planck scale, which in a positive case, would corroborate a desert scenario compatible with: https://arxiv.org/abs/0912.0208Just then, one could finally name such future CERN accelerator the "Ultimatron" ;-)

Peter wrote: They do work on two generations of processors simultaneously

Of course tech companies "do work" to develop products. Now we're stating the obvious. But that's got nothing to do with what Taylor said, namely, companies selling fake products in order to maximize profits, and suggesting that physicists are playing the same game. (Taylor will pretend that he doesn't understand what I mean by fake products)

Taylor is playing a game. He tells us that he is, without question, the least-educated person in this blog, and then he boasts about an undergraduate professor who said he should pursue a PhD (because he's so damn smart!). Apparently that makes him qualified to share his conspiracy theories about tech companies and physicists.

Taylor tells us that he scores in the 99th percentile for English comprehension (he's so damn smart!), so let's see if we can comprehend Taylor's English. What is Taylor implying about physicists?

It seems that he's implying that physicists are playing the same game as Intel and Apple. They're "doling out" incremental improvements in colliders in order to maximize profits. If they weren't so greedy, they would ask to build a collider that could really get the job done. In other words, physicists are deliberately thwarting significant scientific progress that could be accomplished now for the sake of profits. Apparently this is a multi-generational conspiracy.

Are there physicists with self-serving interests? Yes, of course. But if Taylor wants to "darken this comment section" with conspiracy theories, I guess I'll be the one to shine a light on him.

"For example, there are people who are dedicated to finding ever more digits of pi. They are constantly generating more knowledge, but would anyone suggest that we should spend $20 Billion to obtain such knowledge?"

@David Bailey, I'm sure there are such people. And I love them, and I'm sincerely happy that they work on such things. It's even possible that in the course of analyzing those new digits, something very significant is discovered; but at this point I doubt that any theory predicts such results with any degree of confidence.

It would help a lot if particle physicists could tell the public that knowing the value of the Higgs boson mass has led to something new and significant. But I haven't heard this; only that it's supposedly ruled out some conjectures that had no real-world consequences anyway.

there's clearly a physics HEP need for a higher energy lepton collider, to study the Higgs sector. you don't dispute this, do you ?

is there a physics needs for 2 lepton colliders, a circular 100km collider in Geneva and a second linear collider in Japan or USA?

what do you think of conflicting reports about Japan and its proposed ~$10 billion USD linear lepton collider which may be cancelled?

my view is there is a lot of uncertainty about Japan linear collider, and also proposals to build one in the USA, so

why not build the 100km CERN collider and use it as an e p collider to get better information on the Higgs, and hard to find SUSY signals. (though i would prefer china and CERN combine resources and build a 200km or even larger tunnel)

Accepting Bee's arguments based on physics, there still remains one argument left for building a larger collider. The general lay public likes big projects, so there will likely be enough political support for such a project. Then regardless of the results (the lay public won't care much), it's good for Western economies to spend massive resources on technologically complex projects. Today we still benefit from the massive military spending during the Cold War.

Suppose that Germany had not started WWII and that the Soviet Union had become a democratic entity with friendly relations with the West in the 1930s. We would have saved the massive resources used to fight WWII and used in the subsequent Cold War. But had that happened, we would likely not have developed most of the advanced technology that has appeared since the 1930s. We would probably use punch card computers today in 2019.

While resources are not limitless, in practice we're not dealing with a shortage of resources. Otherwise, we would not have a problem with too high CO2 emissions. So, it's actually the opposite, we're spending too much on wasteful activities, e.g. we travel too often on polluting planes to get to far away vacation destinations.

It's just like someone who is obese who feels like he has a lack of energy. That person may object against exercise as that makes him tired, he's only going to spend the least energy necessary for his immediate needs.

Concerning your point"What Intel does is actually very well documented (on a high level, at least; there are lots of trade secrets in the details). They do work on two generations of processors simultaneously. One reason is, of course, to roll out chips with greater frequency. But it also turns out that this isn't so wasteful on their part; there are two kinds of advances you can make in chips. One: clock speed and two: architecture. So the first team produces a new chip that improves clock speed but uses more or less the same architecture. Then the second team produces a chip that keeps the same clock speed, but updates the architecture to take advantage of this improved clock speed. You have two teams with different skill sets, and if they were all working on the same chip simultaneously, they might get in each other's way."

Intel now has changed its development model from "tick-tock" (Tick–tock model), where "tick" stands for die shrink and "tock" for microarchitecture change, to "process-architecture-optimization". Note that for the current architecture Skylake ("tock"), there already exist lots of refreshes (optimizations): Kaby Lake, Kaby Lake R, Coffee Lake, Whiskey Lake. That is why the infamous website SemiAccurate ridiculed Intel's new process using the term "Tick-Tock-Spoing-Thud" (SemiAccurate digs up Intel Coffee Lake specs).

Yes, that is a good point you made and I am sorry in case I didn't make my reasoning clear. The problem is that all the predictions we have for new physics that a larger collider could test are beauty-based. Now, it is correct of course that one can say, let's look nevertheless. But the question is whether that's the best way we can invest the money.

I've plagued myself with that question for a while (indeed if you look back in the blog archive you'll find I used to be in favor of a larger collider). Alas, I've come to the conclusion that this money would be better invested collecting more information on problems we already know of (eg dark matter) or testing sound predictions (early universe, quantum gravity). Or if not that, then we'd still be better off putting the money into something of societal relevance, like AI or fusion power.

In 20 years the situation might change because - so I hope - we'll have more constraints on what dark matter can and cannot be, which would help us to tell whether it is in the range of a larger collider (provided it is a particle to begin with). If neutrinos are Majorana, we may also know by then. I also haven't given up hope that theorists will eventually realize their methods aren't working and think about how to make better predictions. That would help too. Best,

"Therefore, investment-wise, it would make more sense to put particle physics on a pause and reconsider it in, say, 20 years to see whether the situation has changed"

??? Ridiculous statement, Sabine! This proves that you understand nothing about technology issues, you live in your golden tower of theoretical physics... where there is no material development needed, only ideas, in principle white papers and a pencil. Once you stop development in technology you quickly loose the know how, and once it's gone it's gone. Proof is what happened in the usa when similar arguments as yours were put in action, and the SSC project was stopped in its tracks by us Congress. The USA lost the clear advantage they had over Europe in this field.

Investment-wise it would wipe out all of previous investment... that's what would happen.

Business will soon not care about the physicists working on the money eating projects like fusion (ITER) generating only promise and not product (energy). Currently, there is much R&D activity in LENR field - experiment is king, theory is servant.

In most areas of science, success rates for grants are in the 5-20% range, including for theoretically interesting work of immediate benefit to patients, the economy, and the environment. Key skills to develop these areas of research are regularly lost, often forever, due to lack of funding. In this context, the arguments about billions of dollars not being much look obscene!

Leon Lederman coined the term “God particle,” which I think he later regretted. The moniker came because of the idea the Higgs particle gave mass to weak nuclear Z and W^± bosons and fermions and in a sense created this world. In the United States if you make a reference of that sort people will take it not so much metaphorically, but literally. This is in both a positive and negative way. Some in the new age stuff might take it realistically as some new “Age of Aquarius,” and there were, and the religious fundamentalists will condemn it as blasphemy. Recall Dan Brown's novel and movie Angels and Demons and the somewhat embarrassing and mind cringing portrayal of the Higgs particle being held in a sort of bottle.

The God of the Torah and Tanach is a curious somewhat schizoid figure who at times seems wise and benevolent and at others a complete tyrant. God as an ideological system was meant to explain things, but also as a way of organizing societies and controlling people. God is less something we should see as a metaphor in a fundamental particle and more as a supernatural idea of George Orwell's Big Brother. The Christians came about and jacked it up by saying God become a man who said various things we have to believe, who died and rose into heaven so we could have eternal life that was denied to us by the first two humans who were deceived by a talking snake. I think that one sentence about sums it up. If you replace God by Cinderella's fairy godmother, eternal life by life happy ever after and the talking snake by ugly step sisters, professing belief in that will get people convinced you need therapy. The first sentence will get some people angry that you are mocking God --- interesting how replacing a few words can change things.

The religious metaphors aside, and scientists should really avoid them, the purpose of research is to measure things so we can understand patterns in nature according to some formal scheme, aka a theory. The purpose of the LHC or any such program is not so much about tech-spin offs and the like, but in order to answer certain questions. With this new collider the cost globally is not that large and even if SUSY fails to show up or anything else there will be a lot of normative work on the scaling of standard model interactions with higher energy. This might be that final chapter in that sort of physics.

It's interesting to compare the proposed next-generation collider to another Big Science megaproject which did get funded: the Webb space telescope. It's inconceivable that the Webb wouldn't produce any interesting results. On the other hand - unlike a collider - the Webb telescope could fail catastrophically for technical reasons, resulting in the loss of the entire investment. It's not repairable, like Hubble (fortunately) was.

If I had 20 Billion or so, at this moment I would use it for combating global as a first priority. I would reshuffle a lot of money towards that goal. That effort requires also a lot of (applied) basic science.

Today we are happy to have Roberto Kersevan back among us. Roberto works at CERN and, according to his profile at research gate he is an applied physicist who works on the FCC project.

The last time we heard from him, Roberto explained to us that the FCC would "study and discover" the origin of the universe (his exact words) and also was very sure that there are "mathematical, logically solid" reasons why the FCC would discover new physics (also his exact words).

Both of which, needless to say, are wrong statements. He thinks of himself as very funny and his only mode of argumentation are ad hominem attacks.

So you're telling us that we wouldn't be capable of building colliders in the future if we don't build the FCC now? Please enlighten the ignorant masses.

Roberto wrote: Once you stop development in technology you quickly loose the know how, and once it's gone it's gone. Proof is what happened in the usa when similar arguments as yours were put in action, and the SSC project was stopped in its tracks by us Congress. The USA lost the clear advantage they had over Europe in this field.

So we continue to build new colliders for the sake of retaining the know-how for building colliders?

And regarding the SSC, what does that prove? What did the US actually lose? In what meaningful way is the US at a disadvantage to Europe because it cancelled the SSC? In what tangible ways would Americans and the world be better off if the SSC had been built?

Roberto wrote: So, Alistair... is that too much for you?

Insulting people is always a good strategy for winning them over. Your copy of How to Win Friends and Influence People must be well-worn.

Roberto wrote: 600 million citizens of the CERN funding countries.

You've even got babies paying for a new collider. You'll do anything to lower the per capita cost. :-)

If each citizen of the EU gives just one cent to me, I promise I'll do something worthwhile with it.

@Sabine, Roberto, TannerI'd like to make a couple of comments on two topics I know relatively well.First plasma wakefield accelerators. I remember a conference I attended in the 90s in Greece, where the organiser was telling the local press that laser-based accelerators were a decade or two away. It appears that they are still "a decade or two away" today. I will believe when I see one working. The same for nuclear fusion energy. Certainly, the people who advertise these research areas are making wilder promises than HEP physicists.

Second comment, perhaps more fundamental. I've been working with people who develop and use ultrafast laser sources. Experimentalists have bee developing ever shorter pulse durations, from picosecond in 70s to fs in the 80s, and attosecond nowadays. These technical developments have made possible a lot of fundamental studies in physics and chemistry (like imaging chemical reactions in real time). However, the experimentalists that developed such laser devices did so just for the sake of it, because it was an intellectual and technical challenge. Many of the applications could not be and were not forecast beforehand. The process was entirely technologically-driven, and the results in terms of basic physics and chemistry came later. There are of course differences, but a similar logic may also apply to accelerator physics.

From the FIAS website:"At FAIR, an unprecedented variety of experiments will be possible, allowing physicists from all over the world to gain new insights into the structure of matter and the development of the universe, from the Big Bang to the present day."That's not much better than CERN, isn't it?

Why is CERN fixated on the Standard Model? CERN is European Center for Nuclear Research. Why is it not doing research on nuclear fusion? Never mind ITER. Tokamak is 1950s technology. Fusion research is stuck in the 1950s. CERN should develop and experiment with new fusion technologies in competition with ITER. May the best physicists win.

Fusion research should be put on the table and debated among CERN physicists. Funding for fusion research is easier to sell than a bigger collider because it has economic and commercial potential.

@Enrico,Your comment is totally out of touch with reality. CERN physicists and engineers have no experience whatsoever with fusion, it's just not their job. There is already an international collaboration on nuclear fusion, ITER, and it would make no sense to build a second competing one.Second, CERN does not equal LHC. There are other valuable experiments running at CERN, notably on antimatter.

As Opamanfred says, CERN isn't pursuing research related to fusion. I think this is a terminology confusion. For one, the research on nuclear fusion that concerns power plants mostly falls into plasma physics, not nuclear physics. The other thing is that CERN's name is associated with nuclear physics mostly for historical reasons. As you can read eg on the CERN website:

As an aside, Nordita (where I worked until a few years ago), was funded in Copenhagen a few years after CERN, when the CERN theory-people moved to Geneva. Its name stems from (the Danish expression of) "Nordic Institute for Theoretical Atomic Physics", but today the research they conduct has little to do with atomic physics. I guess the lesson is that science changes faster than institutional names ;)

@SabineYou are right of course with your last post. But, in my experience, the general public makes little, if any, difference between atomic, nuclear or particle physics.And even institutional names are misleading. For instance UKAEA is the UK "atomic" energy authority. But it should rather be "nuclear" energy, as we are talking about fission and fusion.

"Therefore, from an investment point of view, it would be better to restart physics and re-examine it in, say, 20 years from now."

A break of 20 years would result in a very important loss of know-how. The savings realized would certainly be wasted to rebuild this know-how. To build a collider, it is necessary to combine knowledge as diverse as experimental and theoretical physics, but also civil engineering, geodesy, electronics, computer science, material science, etc.

There are some hundred particle colliders in the world. It's not like with not building the FCC there won't be any accelerators in operation. If you are worried about loss of knowledge, you need a knowledge management plan. Saying that we need to spend $21 billion just to pass on knowledge over 20 years is not going to convince anyone to spend this amount money.

Sabine,Thank you for your reply.The transmission of know-how does not depend solely on an archiving system or a knowledge management plan. CERN's collaborators possess an immense knowledge that would be lost. This should be enough to continue investing in a new (or upgraded) collider. The West has already lost enough industrial know-how in recent years.

No other accelerator comes close to the engineering complexity of the LHC. Also, no one is saying that avoiding the loss of knowledge is the primary reason for building the FCC. But since you suggested having a 20 year "pause" before deciding, people are just pointing out that in the event where a collider would be built, this would result in a massive waste of resources (even with a knowledge management plan, some parts are outsourced to suppliers which would likely disappear). Of course if you want to put the probability of building it close zero, then the expectation value is maybe not so bad for taxpayers.

I also notice you haven't replied to any of the commenters asking about the FCC-ee or linear collider, which are essentially Higgs factories and would be built for very different reasons than the ones you dismiss in your blog.

The current thinking goes in the direction of first building a 100 km e+e- collider. This has a running time of 15 years, and is estimated to start operation about 18 years after project start. The total price tag for this is 11.6 BCHF. Following this, mankind will know more and our children and grand children can then decide whether they (still) think it is a good idea to spend the additional 17 BCHF for an upgrade to a 100 TeV proton-proton collider. (Of course both energy reach and price is based on todays primitive estimates. In 2053 people may be much more clever). If they do go this way, we are talking about a 70 year time span. Yes, that sounds slightly crazy but remember the LEP/LHC tunnel: Physics from 1989 to 2037, viz 60 years.

So, you 20 B$ number is somehow wrong in both directions: Too high for the first phase; too low for the full programme.

Anyway, even 11.6 BCHF is still a lot of money. But in my view the project is highly worthwhile. Like LEP, FCC-ee will be able to perform precision electroweak measurements which probe the the Standard Model at the quantum level. I am sure you know the LEP history: The precision measurements were first able to predict the top quark mass (173+13-10 GeV) shortly after which the Tevatron was able to find it exactly at the mass where it had been predicted. Then, knowing the top quark mass the precison measurements became sensitive to the Higgs mass. The predicition of 98+25-21 GeV from precision measurements were confirmed by the direct discovery at the LHC as 125 GeV.

So, electroweak precision measurement have been proven to be an extremely powerful too. However, why would anybody want to continue these now? Now, we have no top quark and no Higgs boson to make predictions for. Now, the Standard Model is complete. Well, that is exactly what makes precison measurements even more interesting! If there really is no New Physics beyond the Standard Model, all of our precision measurements should agree within the framework of the SM. If they don't we cannot any longer parameterize away the disagreement by "trivial" effects as the top quark mass and the Higgs mass. This time it is serious! Any disagreement would point directly to New Physics: new particles which enter through loop diagrams. People (theorists, I am an experimentalist myself) make these effective field theory expansions (SMEFT) which have something like 18 operators with associated Wilson coefficients. With the predicted FCC-ee precisions this method shows we will be sensitivity to interaction scales spanning from 6 TeV (for the weakest mode) all the way up to 75 TeV (for the strongest). Of course, we hope to find deviations. But even if we don't, wouldn't that be wonderful: It would rule out probably nearly all of the crazy models your theory friends continue to cook up. SUSY would then probably (finally!) be dead. Or perhaps that this too naive...

I could go on and on and on. I joined this project 6-7 years ago based on reasoning which is not too far away from what you describe in your book and on your blog. As many experimentalists, I was/am tired of all of the fruitless theories being cooked up. I really think we need some powerful experimental input which can (perhaps?) put the thinking back on the right track.

Of course FCC-ee can do much more then described above. Looking for lepton flavour violations is one of my personal favourites in 5 x 10^12 Z decays.

You simply state that knowledge would be lost and that would be a problem, disregarding what I said. To repeat. Not building a larger collider would not mean that there are no particle colliders. There are several hundred of those in the world. Knowledge managements plans can and should be developed. I would totally be in favor of funding those.

You write that "the transmission of know-how... should be enough to continue investing in a new (or upgraded) collider".

I do not think that's a convincing argument, and I doubt anyone else thinks it is. (Besides, of course, particle physicists.) This argument merely demonstrates an unwillingness to even contemplate the situation.

"Also, no one is saying that avoiding the loss of knowledge is the primary reason for building the FCC."

Funny then that that seems to be the only reason particle physicists have offered me so far.

"Of course if you want to put the probability of building it close zero, then the expectation value is maybe not so bad for taxpayers."

Yes, someone should make cost-estimate for that. Excuse me for not being convinced by particle physicists who think that it would be a good investment to build a particle collider.

"I also notice you haven't replied to any of the commenters asking about the FCC-ee or linear collider, which are essentially Higgs factories and would be built for very different reasons than the ones you dismiss in your blog."

I do not "dismiss" reasons, I am explaining why they are not sound reasons. Particle physicists, on the other hand, dismiss my arguments, as this comment section vividly demonstrates.

Regarding all those other plans. Look, may day has only 24 hours. I cannot as one person come up with a cost-benefit estimate that posits all possible collider options against other investments. But, yeah, someone should do it. They should not forget that "no collider" is an option too.

I can not imagine that ESA or NASA abandon the space exploration because we have aerodromes and/or because there are plenty of interesting things to study on earth and/or because we suppose that we know all cosmic objets. Every step for further scientific knowledge is welcome.

I see that people say that FCC-ee (like ILC) is essentially a Higgs factory.

It is right that it is a Higgs factory. But it is much more than that!

FCC-ee is the ultimate (no other suggested machine exceeds it at any of the points) factory for Z, W, Higgs, and top. And also for heavy flavours like b quarks and tau leptons (more decays than at the dedicated SuperKEKB collider which is currently under commisioning and in more favourable conditions, with higher boosts and thus better particle identification).

For our complete physics programme all of the four energy points are essential. The Higgs is a wonderful particle to study. But so is the Z, and the W, and the top.

Well, here I have to admit that the Higgs is indeed special. It is the only fundamental(?) scalar particle in nature. If we could get to 3-4 times more Higgses than listed above, we could make the *discovery* of the triple Higgs coupling. Which would seem an essential measurement.

ESA and NASA both operate many missions whose data is of relevance for ecological and geophysical planning, as I am sure you know. Space exploration further is of obvious relevance for the future of mankind, if you believe it has one. Neither is the case for high energy particle physics which is fapp useless.

Look, I am all willing to contemplate that TeV-scale particle colliders will one day find a good purpose that benefits a lot of people. But I see such applications hundreds if not thousands of years in the future. I am not saying that it's something we should not do. I am saying it's not the right time to further invest in it. The well-being of our society depends on continued progress in the foundations of physics. What we invest into is not a decision that should be made just because it wouldn't be nice if some particle physicists were to become unemployed.

I think you are (in a nutshell) delivering the arguments that particle physicists should make.

Personally, I don't think the Higgs-selfcoupling is worth $10 billion, but personally I also think that what I think doesn't matter much. My issue is really with the attempt to deceive the public about potential payoffs.

@Mogens From your point of view, will it have sense to perform collision of two electron beams, as a SM control experiment to prove the generation of electron-positron pairs. If not, then why ?Best,Valeriy Tarasov

Thank you for your reply which I am very happy with. I follow you a long way with respect to the your arguments about deceiving the public, as you put it. Actually, I think it may be worse: We as a physics community sometimes deceive ourselves by repeating the same arguments over and over again without inviting the individual to make her own judgement. Group thinking in other words. Perhaps this is to be traced back to our educational system. Or perhaps it has to do with the way we recognize people in science. Those who repeat have a better chance of promotion than those who stop and ask questions. All that stuff you and Peter Woit write about.

As to your argument that you don't think the Higgs self-coupling is worth 10B$, I also agree. This should be clear from my comments where I described a major research programme which the FCC-ee will be able to do during 15 years of operation. Measuring the Higgs selfcoupling was a "small" add-on to this.

Firstly, it is too early to say "that CERN intends...". There is absolutely no decision. And when I write about "our" plans, I am merely talking on behalf of a relatively small group of CERN users which for 6-7 years has been pursuing the idea that CERNs next collider should be the e+e- collider I describe. This has not been (and probably still is not) the way the main winds blow at CERN. But we continue working hard and argue our case, and for the time being we air some optimism that the scientific arguments will win in the end.

As to you question about a linear versus a circular e+e- collider, clearly I have my preference. That explains why I work on the project I work on. What a linear collider can do for you is to go to higher energies. The circular collider is basically restricted to the below 400 GeV range due to synchrotron radiation. If you are interested in the below 400 GeV range, build a circular collider. If you want to go higher build it linear. If you read my previous comments, you will see that the below 400 GeV range has an extremely large physics potential. Above 400 GeV? There are arguments which have been carried forward, and still are even though we have been finding ways around that need by usign the data in clever ways:

a) The triple Higgs coupling: It is argued that you need to prodice a pair of Higgses to measure this and 400 GeV is simply not enough. We have proven that you can do this job even better using again loop diagrams. The Higgs production cross section depends at the percent level on this coupling so by measuring precisely the energy dependence of Higgs prodction we extract this coupling.

b) Higgs coupling to top quarks: Here it is actually true that you need higher energies. But this coupling has been already established at LHC, and it will be measured very well at HL-LHC before the turn-on of CERNs next collider.

c) Top electroweak couplings: Here we show that we can do the job by measuring the polarization of the final state top quarks produced at our highest energy point, 365 GeV.

Another reason to go higher in energy could be to do "discovery physics": To look for new particles in this new range. However, by now with the knowledge we have collected at the LHC, I think it is rather unlikely there is anything to be found there.

Let me also say this: Some people have spent 20 years or more to struggle for the ILC. It is not funny for those guys it they see that the world accepts the arguments I put forward. 20 years is a hell-of-a-lot of time. So there are very strong feelings involved in here. Friendships can get lost.

I my view:If the world can allord both, why not.If we can afford only one, well...

Roberto Kersevan wrote:"You forget to say that Intel, like all other high-tech companies, profit from decades of publicly-funded R&D, on subjects that at the time they had been studied were as 'useless' and 'expensive' as the [sic] his vision research is. You simply lack the good perspective of things."

I've worked in engineering & management positions in the semiconductor industry for nearly 40 years. While "publicly-funded R&D" benefit is not zero, it's FAR less than you might imagine, and while a proximate source might be government-funded university research -- an ultimate source is taxes paid by Intel & its employees.

Your sentiment is that of the statist/collectivist former US president Obama, who stated in 2012 "If you've got a business – you didn't build that" ... the false belief that central governments are the primary fount of all knowledge and prosperity.

Technical question: I seem to remember from back when I still sat in lectures about experimental particle physics that circular lepton colliders were pretty much maxed out with LEP and that bremsstrahlung losses argued strongly in favour of linear accelerators. What has happened to that? Do I misremember? (Entirely possible, that was pre LHC first light)... Or do I remember correctly, and did somebody just make a statement that already wasn't true back then? Or has something changed (eg with our knowledge of the Higgs mass)?

"CERN physicists and engineers have no experience whatsoever with fusion, it's just not their job."

Then hire physicists and engineers with experience in fusion. With your logic, we would not have electricity today. There were no electrical engineers when Volta and Faraday were experimenting with electricity. Imagine if they said, "we have no experience in electricity, it's not our job"

"There is already an international collaboration on nuclear fusion, ITER, and it would make no sense to build a second competing one."

Did you read my post? Who said build a second Tokamak to compete with ITER? The private companies doing fusion research don't buy your logic. And they put their own money not taxpayers' money. That includes Bill Gates and other hard-nosed investors.

"CERN does not equal LHC. There are other valuable experiments running at CERN"

Sure. So the choices are: bigger collider or nuclear fusion or other valuable experiments. Why is the discussion only about the benefits of a bigger collider? You seem to be suggesting they already have other experiments so it has to be a bigger collider.

Your comment is totally in touch with reality of myopia.

Mogens,

Your comments show CERN physicists' fixation with SM. To carpenters, everything is woodwork.

I neither have the time nor the expertise to offer cost-benefit evaluations to compare different future collider options with each other. That's a task which would keep a committee busy for the better part of a year, and someone certainly should do it. If they do so, they should not forget that "no new collider" is also an option.

Your probably remember right. This was what was repeatedly stated back in days when the the wind was blowing towards linear colliders. Synchrotron radiation increases as the 4th power of the beam energy (actually the Lorentz gamma factor) and falls only as one over the radius. So, you meet an energy wall which you cannot really mitigate by increasing the bending radius. Already in 1976 Burt Richter of SLAC wrote a paper where he showed that up to 400 GeV collision energy circular colliders would be competitive to linear ones. This is still true. For the physics case we pursue, 365 GeV is the highest energy point we need since we have crossed the ttbar production threshold. Alas a circular collider is the optimal choice.

The cryogenics of the HE-LHC magnets do not fit into the small LHC tunnel radius, so excavation would have to be done over 27 km. This plus the high cost of the magnets brings the estimated cost close to the FCC-ee price tag. And it would probably take 15 years from HL-LHC closure to a possible HE-LHC startup. So, with a rather limited physics potential, not really an attractive option.

You stated yesterday that you do not think a measurement of the triple Higgs coupling is worth 10 B$. I tend to agree with you on that. But that is of course also not what we are talking about here. The physics case of the FCC-ee is much, much larger, as I have tried to argue and as is explained in detail in volume 2 of our cdr at http://fcc-cdr.web.cern.ch/. So, can I ask, if you think 10B$ is still too expensive for all of that? If so, what would, in your view, be an adequate price tag. I believe that is a valid question, since you do argue on the basis of price that you are against a new collider. What is your pain threshold?

"ESA and NASA both operate many missions whose data is of relevance for ecological and geophysical planning,"

There are certainly biologists, meteorologists or physicists who will argue about the uselessness of ESA, NASA and space exploration in general. After all, there are enough ground measurement equipments to determine next week's weather or climate trends without all these satellites and expensive sensors. Some biologists will prefer to study biological systems in situ without sensor systems they find useless.

Each of these approaches (big sience / table top science / in situ observations) is justified. Let's not destroy one over the other, they are complementary.

Today the SM describes "all" of our data. The physics community seems to believe there is something beyond. How do we find that? a) Shoot blindly in all directions and see if there should be any new physics there, or b) measure with larger precision SM properties and look for violation which could direct our later direct search. Not since the 70'ies has any unexpected particle been found through random search. All "discoveries" since then were directed by prior precision measurements. Neutrino oscillations which are arguably beyond-SM physics were also discovered through precision measurements.

I know that such a collider would measure some other constants to more detail, maybe find some new composits, check in on some anomalies, and so on. Point is, there's no reason to think it'll find anything that isn't explained by the standard model. We seem to agree on that.

I don't know how my personal pain threshold matters. As I said a few times, what is needed here is a comparative cost-benefit estimate that not only includes colliders but other options too, including "no new collider" and other experiments. The reasoning I offered is simply that a larger collider is pretty much the most expensive thing you can think of, the risk of "nothing new" is high, and that puts it in the corner of "high cost, low benefit" even without looking much into the details.

To offer some numbers. Look eg at Wendelstein 7-X a nuclear fusion project that costs about 1 billion, the WFIRST telescope costing about 2 billion, the planned Einstein Telescope, which is a gravitational wave detector coming in at about a billion too (or so I read), and the SKA whose total cost is estimated to be 1.8 billion. The first of those projects has a high societal relevance, the last two will deliver more information about already-known puzzles. WFIRST is somewhere in the middle, probing an existing puzzle (the dark sector) and having societal relevance (I'd argue mapping exoplanets is a preparation for space exploration). I consider those expenses well-justified.

For anything more expensive than that, I expect to hear a *very* good reason for an investment. The LHC had such a reason (so had the colliders before it). The FCC does not have such a reason. It's not a particularly deep argument. I just want people to understand what the potential payoff is of making such an investment.

Yes, they will argue, and such arguments are necessary. To make wise investments we have to hear them all out and not omit relevant information. That there is no reason a next larger collider should see anything new is extremely relevant information to evaluate the potential of such an investment. We cannot build all experiments we'd like to have, so your idea of "Let's not destroy one over the other" doesn't work. We have to decide.

Sabine,Perhaps particle physics (and string theory) have received "too much" investment and attention compared to other fields of physics. It is your opinion and it is an acceptable one.If there is a problem, it seems more sociological or administrative, but it's not a scientific one. You are attacking particle physics and string theory on the scientific battleground, I think you should argue on a sociological or administrative ground if you disagree with the actual investment strategy.

Clearly you haven't read my book, otherwise you'd know that I point out very clearly the major problem is a sociological and administrative one and by no means specific to particle physics or string theory. These problems, however, have created actual scientific problems.

It's not my opinion that particle physicists' predictions for new physics beyond the standard model have been wrong for 30 years, it's a fact.

"It's not my opinion that particle physicists' predictions for new physics beyond the standard model have been wrong for 30 years, it's a fact."

Ok, maybe you are right and there is nothing beyond the SM (the SM is the whole story) or maybe the particle/string physicists approach is wrong ... or maybe we need new or extended experiments.

Nevertheless, building a new collider “may” lead to new discoveries. If Hans Janssen had not build the "first" microscope we would not know nothing about cells, microbes, proteins, ... People in the 16th century may well have said “Come on Hans, you are wasting your time and money”.).

We don't live in the 16th century. Experiments in the foundations of physics have become much more difficult and much more expensive. This means we have to decide very carefully what to do. We have been rather careless in the last 30 years, which is documented by the long string of experiments that delivered null results. It can never be excluded that an experiment will find something new, so saying that it may happen is not a useful argument to make a decision.

Tycho Brahé's observatory at Uraniborg was surely very expensive for his time and people may have complain about all this "waste of money". He produced data that helps Kepler to state the laws of planetary motion. It seems very difficult to decide "in advance" if experiments will be fruitfull or not. Very often, discoveries are just by-products (think of Becquerel). We should not close doors "a priori".

I think HEP really needs a dose of philosophical thinking - not another huge budget!

As the years have gone by, the prospect of science reaching the fundamental layer of physics, seems to have become ever more remote, and ever less relevant to everything else. Indeed I now wonder if physicists would ever even recognise that they had reached the ultimate explanation - even if they got there. Wouldn't there always be the lure of still higher energies?

The number of stable particles is small, compared to the zoo of particles that are found in modern accelerators, the most recent of which last for less than the time it takes for light to cross the diameter of a proton! The philosophical question is what does this really mean, and does exploring further and further down the energy axis even make sense?

I also feel that huge sums of money always bring corruption. For example, there are many medical doctors who argue that we are being fed too many pharmaceuticals because Big Pharma bribes (in effect) senior doctors who devise the health guidelines:

@enricoSorry , but you really don't seem to know what you are talking about.You can't turn a particle physics lab into a fusion lab overnight. It would take decades, all the infrastructure and expertise should be renewed.

And you want to "hire physicists and engineers with experience in fusion" to do what, exactly? Just send them there, pay millions, and tell them "hey guys, now come here and discover some fusion device that works". Never mind that some brilliant physicists have already been trying for 50 years.

There are indeed private companies getting involved in fusion today. But most of them are working on, guess what, tokamaks! And for good reasons: it's a well understood configuration and they profit from decades of publicly-funded research. Indeed, they mainly employ physicists coming from the fusion public sector.It's a great thing that private investors get into fusion research, but they may also discover soon that it's harder than they think.

Then there are other concepts, like inertial fusion, which also drain millions, but they have military applications so the millions are easier to find.

How likely is it that an FCC will tell us anything new about neutrinos?

Sabine,

WFIRST, the SKA, and (maybe) the Einstein Telescope all have great potential to make serendipitous discoveries, some of which could be as unexpected as Dark Energy was. This potential is widely accepted, though for obvious reasons it doesn’t get much mention in the detailed cases for why they’re worth spending $$ on. As I understand it, an FCC has quite limited serendipitous potential (maybe Mogen could comment).

Possibly not a good example as the observatory was closed after 30 years due to loss of sponsorship. Fortunately by then the data collected has allowed Kepler to formulate his ideas of planetary motion.

Tycho's observatory lasted 30 years from start to finish. The LHC is roughly the same age...

"We have been rather careless in the last 30 years, which is documented by the long string of experiments that delivered null results."

As always I am intrigued by your arguments.

Of course null results are not what we would like. Or is it? Can I use the example of dark matter? Here there has been numerous experiments, needless to say all with null results (except probably DAMA but that is another story). Does your argument then mean that all (or some) of these experiments have been worthless? I guess not? What would we know about dark matter if they had not been performed? Is it not valuable to know that DM is probably not a WIMP? If you agree that this is of value, it is probably a question of when to stop. When to close the book. And somehow you seem to have come to the conclusion that this moment has come now? At least when we talk about accelerator physics.

For the FCC-ee, with its precise testing of the quantum mechanical coherency of the SM, I have my own private no-lose theorem which you probably do not subscribe to. There are two possibilities: a) We could end up with the result that the SM is internally consistent up to the ~50 TeV mass scale that the FCC-ee is able to probe, or b) we could prove the opposite which would point directly to new physics. For me both of these results would be very valuable information, however one certainly more exciting than the other. I admit that there is a possibility that the SM is all there is. But personally I believe we have to take this potentially last experimental step in order to ascertain that "new physics" is not just around the corner from where we are standing right now. I am of course aware that, even if all we do is to confirm the SM, some people could come back and ask for yet another larger machine. And this could continue forever. So yes, where we stop has to be discussed.

"How likely is it that an FCC will tell us anything new about neutrinos?"

Not much about conventional neutrinos.

However there is the so-called nuMSM theory by Mikhail Shaposhnikov. Here the SM is extended by the only obviously missing ingredient: right handed neutrinos. As far as I recall, this theory has the potential of solving "all of our problems": Dark Matter, matter-anti-matter asymmetry, and the origin of neutrino masses. Normally a W boson would decay to a neutrino and a lepton (in 33% of the cases, the rest to quark pairs). In the nuMSM model, there is a mixing between ordinary neutrinos and these new righthanded neutrinos (N). And thus there is a possibility of W bosons decaying to N plus a lepton. The N would possibly (depending on its coupling and thus its lifetime) decay after a finite flight distance inside the detector volume and appear as a diaplaced vertex from which two or more charged tracks appear. This has gained increased attention recently and searches are being carried out. No results so far.

Please notice that Shaposhnikov's model cures the "deficits" of the SM not by postulating new particles at higher mass scales, as it is more customary, but at relative low mass scales, but on the other hand extremely weakly coupled. In such cases it is far from obvious that a new accelerator at the "energy frontier" is the right tool. On the other hand, here again an "intensity frontier" machine like the FCC-ee has an enormous potential. Of the 5x10^12 produced Z decays, 20% or 10^12 will decay to neutrino pairs. Again some fraction of these could decay to one ordinary neutrino and one right-handed N. And again we may see detached vertices. It has been shown that this search is sensitive to a substantial part of parameter space which is allowed by cosmological constraints. A much larger sensitivity than LHC and probably even FCC-hh.

Let me say, that personally I find something like the nuMSM interesting. When you teach a class in introductory particle physics, every year you will get questions from a student of the kind: "Do right-handed neutrinos really not exist, or is it only that they do not interact at all, so that we cannot see them?" What can I give of answer to this? I would really like to know.

Indeed, null results are also results, but when it comes to theory-development they are not particularly useful results. What we need to make progress in the foundations of physics is evidence of some new phenomenon. If we are not careful enough in picking the right experiments, we'll end up in vicious cycle. I think we have been in this cycle (null-results, no guidance for theory-development, bad predictions, null-results...) since the 1980s. You don't have to agree on my interpretation of recent physics history, but the lack of progress in theory development is undeniable.

"Does your argument then mean that all (or some) of these experiments have been worthless? I guess not?"

Those experiments were good ideas at the time, but if we do not learn the lesson from the null results that renders them worthless. Yes, the question is when to stop.

"somehow you seem to have come to the conclusion that this moment has come now? At least when we talk about accelerator physics."

I do not think accelerator physics should be discontinued. I just think it's not the right time to invest in a next larger collider. I'm not half as extreme as people say I am ;)